History and Theory of Psychology: An early 21st century student's perspective
Paul F. Ballantyne, Ph.D. 2008©.
pballan@comnet.caSection 5:
Wax and Wane of American General Psychology (1920-1990s): S-O-R, the Operationist Variable model, and the Crisis of Relevance.
In this Section we'll consider three widespread disciplinary aspects of 20th century American General psychology: The successive expansion of its supposed subject matter (from an admittedly narrow "S-R account" of observable behavior on up to various wider S-O-R accounts of animal or human action and mentality); the gradual adoption of an operationist "Variable model" of empirical research (in its combined experimental and psychometric manifestations); and the ensuing "Crisis of relevance" once the limited descriptive value or methodological confines of the former two aspects started to become recognized.
R.S. Woodworth's initial expansion of the Stimulus-Response account of psychology's subject matter to include dynamic, goal-directed, and interacting Stimulus-Organism-Response processes represented a progressive step as did his (and E.C. Tolman's) contemporaneous efforts to outline an independent-dependent variable model of empirical research. Similarly, S.S. Stevens (1935a, 1935b, 1939) and E.G. Boring et al., 1945 relied upon the tradition of Logical positivism to advocate the adoption of clearly stated operational definitions as a means of subjecting formerly amorphous psychological concepts to empirical inquiry.
Woodworth (1926, 1934) cautioned psychologists not to interpret his S-O-R account of subject matter as a rationale for advocating a strictly linear three-moment view of empirical method, but this finer point of procedure was neither consistently adhered to by Woodworth himself nor was it widely appreciated by other general psychologists. Similarly, critiques of the rather fundamental philosophical and methodological faults residing in the 1930s era Stevens version of operationism were put forward (Waters & Pennington, 1938; Roback, 1952; Ritchie, 1953, and even Stevens, 1951b), but they also failed to sustain the attention of empirical psychologists.
Instead of meeting the central aspects of these cautions and critiques head-on, a discursive-procedural flanking maneuver was carried out. The initial variable model of experimental research and the emphasis upon operational definitions indicative of these two respective efforts to encapsulate how the science of psychology ought to be conducted, were gradually melded with the ongoing ontologically agnostic tradition of individual differences research. This softened form of "convergent" operationism (a.k.a., the convergent validity of indirect measures approach) was intended to allow empirical research of the correlational and experimental stripes to carry on without becoming bogged down in acrimonious ontological (a.k.a., theoretical) or epistemological debates (e.g., realism vs. anti-realism).
During this mid-20th century period of scientistic hubris a tacit professional agreement to remain more or less metaphysically neutral -to abandon the former talk about mental or psychological processes in favor of talk about psychological variables, operational definitions of hypothetical constructs, or convergent validity of multiple measures- is the most striking characteristic of General psychology (see MacCorquodale & Meehl, 1948; Tolman, 1949; M. Marx, 1951; Cronbach & Meehl, 1955; Garner, et. al., 1956; Cronbach, 1957; Campbell & Fiske, 1959).
Furthermore, the popularized version of this "combined" operationalized variable model of psychological research which appeared in mid-1960s through 1970s textbook depictions of empirical procedure (e.g., Munn et al., 1969; 1972; Evans & Murdoff, 1978) remained within the confines of the scientistic mode of assessment. The simple intent of these depictions was to provide students with an albeit "eclectic" introductory portrayal of the assumed disciplinary relationship between our empirical techniques and the so-called organismic or internal psychological "variables" (like motivation, personality, and intelligence) they were designed to measure. Accordingly, however, the structure of the said diagrams was undeniably linear and static with no depiction of the development of psychological processes per se being provided. It was thereby revealed that the combined variable model, like the preceding strictly behaviorist or operationist traditions, constituted a problematic retreat from the very subject matter of psychology itself.
What seems relatively modern or progressive at one historical juncture of the discipline, can also be found to be holding it back at a later juncture -hence the need to periodically reconsider and weigh the available methodological options in order to bring about successive advancements in the discipline. The period of reassessment we are labeling here as the Crisis of Relevance was one such attempt at: (1) reconsidering the Behaviorist and Logical positivist assumptions of general psychological research methods; and (2) broadening our understanding of empirical practice in psychology so that it remains at least potentially relevant to questions of human affairs. The proposed disciplinary remedy (namely: a revised but highly generalized "S-M-R variable" definition of subject matter with its specific theoretical constituents being both empirically assessed along Popperian "falsificationist" lines and propped up by a rickety "dynamic interactionist" metaphor of nature vs. nurture- was itself eventually found wanting in certain respects and the disciplinary fallout from that realization are still underway in mainstream psychology.
The fundamental methodological disjunction between the traditionally quantitative-mechanical focus of variable model psychology in all its forms and the qualitative-developmental nature of ape, primitive, child, and modern adult mentality was not resolved by that era's reassessment of the issues (Koch, 1959-63; Cronbach, 1975; Guthrie, 1976; Kendler, 1981a, 1987; Koch & Leary, 1985; Hilgard, 1987, 1988; Kline, 1988; Royce, 1988; Staats, 1983, 1991). The disjunction not only remained intact, it was both further exacerbated by professional infighting between psychological subdisciplines and even abandoned as "irresolvable" by some of the high-profile metatheoreticians of that extended period (Koch, 1981; Gergen, 1981, 1984; Toulmin & Leary, 1985; Wertheimer, 1988; Leary, 1990; Danziger, 1990, 1997).
There are surely numerous reasons why the relatively progressive intent and potential disciplinary impact of that reassessment era was ultimately undermined in practice. Some of these quite clearly include the institutional or administrative vested interests of its main participants but anyone looking back at that era's assessment of the issues can not help also noting the decidedly narrow Amero-centric scope of their efforts to consider the existing methodological alternatives. In any case, there is simply no denying that late-20th century General Psychology -in not only its mainstream (experimental, psychometric, or clinical-developmental) manifestations but also in its fringe (historical or theoretical) manifestations- had become a thoroughly middle-class, Amero-centric discipline with little serious consideration of the existing methodological alternatives which fell outside its immediate self-serving purview.
The historiographic object lesson we will be working toward from here on in is as follows: The progressive intentions or critical viewpoint of any given psychologist or group thereof is not sufficient alone to bring about the required changes in the discipline. What is needed is the "right kind of psychology." Stating the argument to be made in this Section rather negatively at the outset might help you better recognize and weigh the respective importance of the various remedial arguments as they are presented. The right kind of psychology is one that does not constantly sabotage theoretically progressive and sincerely democratic intentions by: (1) its constrained assumptions about psychological subject matter; (2) by its stubborn analytical adherence to the merely mechanical structure of statistical methods; or (3) by its self-serving motives for carrying out periodic though merely tactical, esoteric, and face-saving professional adjustments (rather than strategic disciplinary transformations) once these proclivities become a matter of public concern.
The present rather damning critique of the discipline between 1920 and the 1990s, will be interspersed with (and ultimately followed up by) some rather specific suggestions as to how the past constrictive methodological assumptions, empirical practices, etc., might still be remedied (revised, augmented, reconstructed) without falling prey to either positivistic scientism or to the outright anti-empirical positions of the Neo-Kantian "Constructivist" camp of psychological metatheory. So hold onto your hats, it is going to be a bumpy ride!
From Watson's S-R to Woodworth's middle of the road S-O-R
In order to outline the early 20th century disciplinary strivings toward a moderate account of psychological subject matter (one that would allow a continuance of research into observable behavior and of what James called conscious mental life), we'll start by contrasting the career of J.B. Watson with the initial part of R.S. Woodworth's considerably longer career in this regard. The contemporaneous debates between E.C. Tolman's moderate "methodological" behaviorism versus the respective radical behaviorisms of Watson and C.L. Hull (up to 1948) will also be drawn upon to indicate the built-in confines (in terms of accepted empirical practice and possible theoretical advance) of that early "molar S-O-R" vs. "molecular S-R" disciplinary divide.
These initial considerations regarding the rationale for the rise of a molar S-O-R account of psychological subject matter, will set the stage for our subsequent coverage of the independent-dependent variable approach, operationism, and the gradual implicit acceptance of a combined operationalized variable model of research. While our initial goal in these considerations will be to note the disciplinary antecedents and overlap in timing between the rise of the S-O-R account and the early variable model approaches to research (in Woodworth and Tolman respectively), the overall historiographical motive will be to understand their deeper disciplinary relationship with what followed thereafter. In other words, the eventual "combined" variable model of empirical research logically follows from the earlier S-O-R account of psychological subject matter. The strengths and problems which reside in the latter spring from those inherent in the former.
J.B. Watson and the disciplinary context for his Behaviorist Manifesto
John Broadus Watson (1878-1958) was raised in a poor, rural South Carolina family by both his mother (a pious Baptist) and at least partially in the absence of his carousing father who left the family when John was about 13 years old. Up to that time John seemed destined to follow his father's unruly example, but by age 16 he was off to Furman University (Greenville, SC.) for a traditional education in the classical curriculum conversant with his mother's aims of making a him a minister. In his senior year, John applied to Princeton Theological Seminary but ended up staying on at Furman for an extra year to receive a Masters degree in 1900 (see Fancher, 1990). During that pivotal year, his mother passed away and Watson was thus freed from all family expectations.
He initially enrolled in the then combined University of Chicago graduate philosophy and psychology curriculum but quickly became disenchanted with John Dewey's rambling teaching style. He then switched over to doctoral research in the new field of animal psychology (under J.R. Angell and a physiologist called Henry Donaldson) receiving a Ph.D. in 1903 (see Watson, 1936).
It was customary for American graduate students of this period to participate as subjects in the empirical studies ran by their professors and by other students. This was a role which Watson found rather frustrating: "I hated to serve as a subject. I didn't like the stuffy, artificial instructions given... I was always uncomfortable and acted unnaturally" (Watson, 1936, pp. 274-276).
One of the most notable studies which Watson participated in was Angell's on the localization of sound (Angell, 1903b). The blindfolded "observer" was seated in a chair at the center of a circular device that could be tilted or rotated to generate a tone at any point in the surrounding space. While subjects were asked to provide post hoc introspective reports of their "conscious experience" of the experimental procedure, the major empirical focus of the study was on the "accuracy" of the elicited pointing (the measured correlation between the position of the generated tone and the observer's pointing).
Watson's participation in this experiment is not only notable because he would eventually propose that "observable behavior" is the only proper subject matter for experimental psychology, but also because it is indicative of the immediate antecedent context of Americanized research within which that proposition would be advocated. As Thomas Leahey puts it: "[In] the experiments of this entire period [roughly 1900-1912] one finds, with the exception [of those] from Titchener's laboratory, introspective reports being first isolated from the primary objective results and then shortened or removed altogether" (1991, p. 157).
One can well imaging Watson's early graduate-school days reasoning in this regard: If introspective reports from human subjects are so ancillary to the central concerns of even so-called "functional" psychology research, why not do away with them altogether? If reference to consciousness in either its structuralist "content" sense, or in its functionalist "utility" sense does not serve as a reliable source of publicly verifiable data, why blame it on the inadequate training of those providing such reports? Why not attempt to adopt a third approach, one that abolishes introspection as a method for experimental psychology?
Watson's Animal Research
Rather conveniently for Watson, however, his doctoral research (published as Animal Education, 1904) utilized animal subjects. It investigated the effect of various surgical interventions on the ability of albino rats to gain entry into a specially constructed wire box containing food (see Chapter 2 of Ballantyne, 2002 for a picture and further elaboration). This new laboratory animal had first become available to Americans in 1896, when Adolf Meyer, a young Swiss neurologist convinced Donaldson at Chicago to use them for his studies on nervous system development (Boakes, 1984; Demarest, 1987). Donaldson, in turn, lent Watson the necessary cash to publish his dissertation in exchange for Watson's continued help in maintaining the University of Chicago animal laboratory. Watson also served out a part-time instructorship there (1904-1908) before managing to negotiate a position as full professor of "Experimental and Comparative Psychology" at Johns Hopkins (in Baltimore).
Watson's next notable Chicago era work (published in Psychological Monographs, 1907a) attempted to answer the question of how rats learn mazes. It portrayed the rat's maze performance as an additive chain of discretely learned responses controlled by kinesthetic feedback which presumably become increasingly integrated as training continues. A related study, with his first University of Chicago graduate student Harvey Carr (known as the Kerplunk experiment) lent even more empirical weight to this "chain of responses" hypothesis. Once the rats were extensively trained to retrieve food at the end of a long arm of a maze, it was shortened by placing a barrier about half way along. When released into this shortened arm, the rats ran squarely into it -making a "Kerplunk" sound- and seemed to ignore the food located there (Watson & Carr, 1908; cf. MacFarlane, 1930 below).
Throughout his time at Chicago, as well as during the initial phase of his teaching career at Johns Hopkins University (up to 1912), Watson maintained that the behavior of rats and other lower organisms warranted scientific investigation "regardless of their generality" (Watson, 1906, 1907b, 1908a&b). He even conceded that humans in the same situation probably use "ideational" means and "visual imagery" to navigate mazes (see Watson, 1907a). He was, however, becoming bored with the seemingly unresolvable debates between Jennings, Loeb, Pfungst, and Yerkes over the proper criterion for mental phenomena, and human vs. animal thought (Watson 1907a&b, 1908a, 1909). Accordingly his subsequent works increasingly portrayed even human learning as the additive development of simple into more "complex motor habits" (Watson, 1913, 1914, 1919a, 1924a, 1924b, 1930).
The Behaviorist Manifesto
Once free from the early moderating influence of Angell's Chicago functionalism, the first explicit step along this new argumentative path was taken when Watson produced his behaviorist manifesto aimed at the systematic ousting of appeals to unobservable "consciousness" from psychology. This manifesto initially appeared in 1913 and was then slightly revised as the first chapter of his Behavior: An introduction to comparative psychology (1914). In both versions Watson asserts that thoughts and images are sensations arising from events outside the brain. Since these events are "habits" identical to other bodily actions -except that they are more difficult to observe- he applies the label of "implicit behavior" to them and suggests, further, that what we usually call "thinking" in human beings is really subvocal speech: "Now [if] it is admitted... that words spoken... belong really in the realm of behavior as do movements of the arms and legs.... the behavior of the human being as a whole is as open to objective control as the behavior of the lowest organism" (Watson, 1914, p. 21).
In order to support this new behaviorist argument, Watson (1914) begins with a summary account of animal sensory research to date concentrating specifically on the experimental hardware and techniques -such as delayed reaction situations- developed by American psychologists since the turn of the century. Secondly, he outlines various techniques of observational field work including his own work with noddy terns (1908b), followed by an account of maze learning and other "acquired habits" in rats. This, in turn, is followed by a brief report on measured tongue movements while performing experimentally derived thought tasks as an example of "language habits in human beings." This latter evidence, while providing empirical "support" for his subvocal speech hypothesis, was also the most speculatively driven part of Watson's (1914) book. To his credit, however, he openly admitted the limitations of contemporaneous knowledge about such language habits (see also Watson, 1920).
As indicated in Section 4, the professional reception to Watson's behaviorist manifesto was rather muted. Angell (1913), for instance, openly acknowledged the possible usefulness of "behavior as a category" for the description of the objectively observable aspects of psychological phenomena, and Carr eventually adopted a similar conciliatory stance. There are two notable exceptions to this rule however. Firstly, Titchener's (1914) rather defensive reply was that Watson's position poses no threat to introspective psychology because it is "not psychology" at all but belongs more properly to the class of biological inquiry. Secondly, and perhaps more importantly, the particularly "extravagant" motor theory of thought proposed by Watson (the equation of thought with surreptitious movements in the throat and larynx) was readily questioned by McComas (1916) who called attention to the continuance of thought in persons whose throats had been destroyed by disease (Samelson, 1981).
Prior to revising (though not abandoning), these initial overstatements regarding the subvocal speech hypothesis (1920), Watson's research interests and activities had already turned decidedly toward carrying out a series of systematic investigations with human subjects. His joint report with Lashley of their investigations into homing "activities" of birds (Watson & Lashley, 1915) constitutes the last time Watson would spend any considerable time on animal research. Do see Boakes (1984), however, for an excellent account of Watson's early and last research into birds!
Watson's human research
Watson's shift toward human research was most certainly driven by his ongoing system-building ambitions. It was also, however, considerably aided by new and partially serendipitous institutional circumstances which Watson began utilizing toward this end.
The theoretical-technical aspect of the shift came in late 1914, when Watson read the French translation of Bekhterev's Objective Psychology (1907-12). While Pavlov's research on conditional salivary reflex in dogs had been brought to the attention of American psychologists by Yerkes and Morgulis (1909) it was Bekhterev's laboratory techniques -such as the withdrawal of a paw when electric shock was administered as the "unconditioned stimulus"- which struck Watson as both easily applicable to human beings and as one empirical means by which he could support his own claim that "no new principle is needed in passing from the unicellular to man" (Watson, 1914, p. 318).
Accordingly Watson (with the help of graduate student Karl Lashley) set out immediately to construct his "finger withdrawal reflex" apparatus and to then interpret the forthcoming "conditioned" tone-withdrawal responses in a thoroughly additive-mechanical (a.k.a., molecular) fashion as if they resided merely at the level of muscular motor reflex. We will return to this issue later (see Wickens, 1938 below) so let's simply note that Watson was now emphasizing "conditioned reflex" as a possible basis for the empirical prediction and control of behavior in animals and man; and that some of these empirical forays had already progressed sufficiently far to become the main topic of Watson's 1915 presidential address to the APA (Watson, 1916a). Here Watson described initial experiments (done with Lashley) on humans, dogs, and owls, and suggested the new technique might well prove to have wide generality (see also Cason, 1922a&b).
Watson's other 1916 article, Behavior and the concept of mental disease further clarified his intention to gradually expand the application of behaviorist techniques to topics outside of animal psychology. He paid tribute to Freud's insight that early childhood experiences might have a pervasive influence on later adult life but also suggests that "objective" terminology based on the concept of "habit" would be a more useful tool to employ if we are ever to understanding the early origins of neurotic behavior.
The partly serendipitous aspect of Watson's shift toward human research also came in 1916 when a number of Johns Hopkins departments were relocated to a new site outside the central Baltimore city core. Here, unfortunately, the facilities for animal research were inferior to the older facilities (Boakes, 1984). Although Watson's new office located in a Psychiatric Institute afforded him easy access to a possible study population of adult neurotic subjects, he did not have the inclination to pursue that research. Instead, Watson opted to carry out research on infants in a nearby maternity hospital. Infants like rats after all, don't talk back and provide no messy introspective reports to cloud the rather fundamental issues which had captured his immediate interest.
As Watson understood them, these fundamental issues included: (i) distinguishing "learned" from "unlearned" behavior (hence his interest in the infant grip reflex, strength of grasp, and possible environmental origin of hand preference); as well as (ii) investigating the initial scope and possible malleability of so-called "emotional reactions." As first reported in Watson & Morgan (1917) and as later graphically depicted in silent film footage (1919c), Watson evoked the emotional reactions of "fear, rage, and love" in infants (aged within 1 month of birth) by a variety of rather crude means. "Fear" was evoked by sudden loss of support, sudden shake or pull of blanket, and loud sounds. "Rage" was generated by hampering the infant's movements (by holding the head or constricting the arms and legs). "Love" reactions were obtained when the babies were tickled, rocked, or given another form of stroking -including "manipulation of some erogenous zone" (Watson, 1919a, p. 200; see also Watson, 1919c). Watson (1919a) also reports data on the grasping strength of infants collected at this time and makes further comments on the possible environmental origin of hand preference to the great disdain, it should be added, of subsequent developmental psychologists.
The most notable and infamous study arising from Watson's pre-WWI academic career, however, is the one now known as the Little Albert experiment (reported in Watson & Rayner, 1920). Here Watson unequivocally demonstrated the viability of classical conditioning as an agent of behavioral change and also provided possible evidence of an environmental cause for phobic mental disorders (see also Watson, 1919c, 1926).
Was Watson's research unethical?
While the ethical protocols, measurement procedures, and reductive analysis of his pre-WWI research are clearly out of step with our current standards of empirical research conduct and theory (see Harris, Whatever happened to Little Albert?, 1979, and also below), they were nonetheless important and require that we put them into some sort of historical-disciplinary context.
On the theory side, Watson seemed to have empirically demonstrated not only that the stimuli which provoke "emotional reactions" in infants "prior to learning" are decidedly "limited" but also that they are easily manipulated through the technique of classical conditioning. This was at least his view (see Watson, 1919a, 1926). Although the additive associationist assumptions (e.g., that adult human emotion is a mere build up of evoked feeling responses learned by habit from infancy) and mechanical S-R terminology of Watson's analysis are easily recognized today as too confining, let's at least recognize that he had very good disciplinary and empirical reasons for sticking steadfastly to an environmental interpretation of psychology. The only well recognized pre-WWI disciplinary alternative during that period of American psychology (Eugenics) was unconscionable to him; especially because his own infant studies indicated no difference between the occasional "Black" and the more usual "White" babies on the albeit fundamentally biological and crude observations made therein (Watson & J. Morgan, 1917; Watson, 1919a; Watson & Watson, 1928; Watson, 1924, 1930).
It is this wider historiographical context of Eugenics-inspired, outright racist, psychological research and the ongoing rise of psychometrically-guided administrative school sorting technologies (see Ballantyne, 2002, Chapters 1-4) that sheds the best light on both Watson's oft-quoted (1924, 1930) hyper-environmental overstatement; and the candid (less often quoted) tone of the passage which immediately follows after it:
"Give me a dozen healthy infants, well-formed, and my own specified world to bring them up in and I'll guarantee to take any one at random and train him to become any type of specialist... doctor, lawyer, artist, merchant-chief and, yes even beggar-man and thief, regardless of his talents, abilities, vocations, and race of his ancestors. I am going beyond my facts and I admit it, but so have the advocates of the contrary and they have been doing it for many thousands of years" (Watson, Behaviorism, 1924, p. 82; 1930, p. 104).
Within the context of the times, therefore, the ethics of Watson's empirical human research as well as the overzealous additive environmentalism are not as appalling or outrageous as they might appear to the modern reader at first glance. Those labels, belong to the theorists and psychometric practitioners in the inheritance camp whom Watson was arguing against. From their blatant or assumed hereditary viewpoint, these figures (including: Henry Goddard, C. B. Davenport, R.M. Yerkes, Lewis M. Terman, Ellwood Cubberley, and even Henry Chauncey -the first head of the Educational Testing Service) used their own version of an additive mental ladder as well as the new individual and group mental testing technology to do more overall harm to potential immigrants, visible minorities, lower-class job applicants, and generations of both school children and hopeful university applicants than Watson ever might have done to subjects like Little Albert.
Despite knowing when their subject was scheduled to leave the hospital Watson & Rayner, it is true, did not decondition Little Albert. This, as Harris (1979) points out is reprehensible according to our current ethical standards of research. They did, in hindsight, outline a reasonable procedure for "'Detachment' or removal of conditioned emotional responses" and this procedure was later used by Mary Cover Jones (1924) to "uncondition" her subject "Peter." The ethical treatment lesson I guess had been learned.
Watson, like all of his notable contemporaries (including R.S. Woodworth, E.C. Tolman; and later E.G. Boring described below) was struggling to do his best within the context of that early era of psychological knowledge. The same can not be said for figures like Lewis Terman (the progenitor of American "Intelligence" and "Achievement" tests) who took full advantage of a rather repressive sociological context to further his own professional career ends (see Minton, 1988; Guthrie, 1976, 1996).
That repressive sociological context, incidentally, had a rather direct personal impact on Watson's career too. Like his Johns Hopkins predecessor James Mark Baldwin, Watson was forced to resign his chair because of a "sex scandal." He had not only become sexually involved with his research assistant Rosalie Rayner, but also had the audacity to carry out physiological measurements of that "involvement" -a fact which apparently came out as evidence during the process of a rather messy divorce. As noted above, Watson continued to publish books on psychology -including Behaviorism (1924 rev. ed., 1930, 2nd ed.) and The Psychological Care of Infant and Child (1928)- but by the 1930s his main career energies had shifted to the advertising business.
Woodworth's "Dynamic" psychology and the S-O-R formula
As for the ongoing disciplinary standing of Watson's S-R account of psychological subject matter (1920-1938), R.S. Woodworth (1924) had already pointed out that there were at least three other less radical varieties of behaviorism in existence (including that of E.C. Tolman, 1922, see also Lashley, 1923). We'll start with a generalized overview of Woodworth's consensus-building discourse regarding "dynamic psychology" because it sets the stage rather nicely for our subsequent consideration of both the strengths and limitations of his ensuing and constantly amended Stimulus-Organism-Response account of psychological subject matter, as well as the related early "variable" model of experimental research which Woodworth and others outlined.
Influenced at Harvard by William James, Robert Sessions Woodworth (1869-1962) did doctoral research in psychology at Columbia University under James McKeen Cattell, where he then taught during 1903-42. His major works include: Dynamic Psychology (1918); Psychology (1921, 1929, 1934); Contemporary Schools of Psychology (1931); Experimental Psychology (1938); and Dynamics of Behavior (1958). In all of these, he advocated the eclectic use of behavioral, physiological, introspective, or psychometric methods depending on which method best fits the situation of empirical interest.
The task which Woodworth set himself was one of: How to best draw together the divergent empirical concerns and theoretical claims of Structuralism, Behaviorism, and comparative psychology including mental testing into a "middle of the road" psychology that nearly everyone could accept. In this effort, he can be said to have represented the strivings and sentiments of most general psychologists of that era.
Dynamic Psychology: "activity," motivation, and the study of mental life
While trying to define his own "Dynamic Psychology" approach to General psychology, Woodworth was wrestling with the three-way disciplinary standoff between Watsonian behaviorism, Titchenerian introspectionism, and William McDougall's "Hormic" psychology (a form of motivational psychology utilizing an appeal to so-called social instincts). The term "dynamic" was employed by Woodworth (1918, 1926, 1930a) to emphasize the urgent disciplinary need to avoid the unnecessary methodological prescriptions and the unwarrantable exclusion of relevant empirical research which characterized these former psychological traditions.
Similarly, the first three editions of his introductory text (1921, 1929, 1934) also employed a clever consensus-building strategy and thereby managed (along with his Experimental Psychology, 1938) to become by far the most widely used for undergraduate and graduate courses in psychology (Winston, 1988, 1990). In these, as well as in his 1931 historical text, Woodworth adopts the argument that it is in the best interest of all contemporary psychologists to play-down their preconceived metatheoretical differences and concentrate upon the actual empirical practices and results of the discipline; for it is in this way that a relatively noncontentious middle of the road psychology might eventually be worked out.
Thus, while the subtitle of his Psychology: A study of mental life (1921) was most certainly a snub to Watson's radical behaviorism, the opening definition of psychology contained therein utilizes the behavior-friendly concept of mental "activity" which includes analysis of the action of bodily organs:
"We conclude, then: psychology is a part of the scientific study of life, being the science of mental life. Life consisting in process or action, psychology is the scientific study of mental processes or activities. A mental activity is typically, ... conscious and we can roughly designate as mental those activities... that are either conscious themselves or closely akin to those that are conscious. Further, any mental activity can also be regarded as a physiological activity, in which case it is analyzed into the action of bodily organs, whereas as 'mental' it simply comes from the organism or individual as a whole. Psychology, in a word, is the science of the conscious and near-conscious activities of living individuals" (Woodworth, 1921, p. 17, emphasis added).
This broad "activity" concept struck a congenial cord with moderate behaviorists including Harvey Carr (1925) who (as indicated in Section 4) adopted it though in an albeit less effective manner as a theoretical foundation-stone for his own introductory text. Both Woodworth and Carr are in agreement that the theoretical concept of activity is one in which the long-standing methodological dichotomies (subjective-objective; internal-external; vital-mechanical; whole-part; biological-individual, etc.) might be captured and made amenable to study in experimental settings.
"Activity" itself, Woodworth later defines as "any process which depends upon the life of the organism and which can be viewed as dependent upon the organism as a whole" (1930a, p. 328). In other words, it is a broad concept which includes (subsumes) not only physiological processes in the brain and spinal cord of an intact organism; but also the bodily movements, unconditioned and conditioned reflexes, and observably goal-directed actions or consciously motivated behaviors of those living organisms.
"Behavior" he suggests rather early on in the 1921 text, "would be a very suitable [stand-alone] term, if only it had not become so closely identified with the [Watsonian] 'behaviorist movement'... which urges that consciousness should be entirely left out of psychology, or at least disregarded" (p. 2). Reiterating the argument he writes:
"What the behaviorists have accomplished is the... overthrow of the doctrine... that introspection is the only real method of observation in psychology.... But we should be going too far... to exclude introspection altogether.... Let us accumulate psychological facts by any method that will give the facts" (Woodworth, 1921, p. 13).
Likewise, while Woodworth (1930a) argues that psychology ought to include introspective analysis (it should utilize experiential, phenomenological methods where applicable) he also explicitly states that there is "nothing in that requirement" which limits psychology to "the study of [Titchenerian] sensations." In his opinion, both experiencing and acting (a.k.a., behaving) should be accounted for in the new experimental psychology, and Woodworth is careful to point out why this is so:
"With the advent of laboratories and groups of psychologists the subject of an experiment became typically someone other than the investigator himself, and psychology became in practice the 'psychology of the other one,' to use a pregnant phrase of Max Meyer [1921]. But if we are studying the 'other one,' there is no excuse for limiting the study to his 'experiences' [a la Titchener]; we should study his behavior as well, if only to round out our study and to see things in their relations.... for neither behavior... nor experience... is anything but a fragment when taken alone" (Woodworth, 1930a, p. 330, emphasis added).
Woodworth's (1930a) climatic argument for the inclusiveness of subject matter and place of psychology in a hierarchy of science runs as follows: Since both introspective experience and behavior are dynamic and goal-directed rather than passive, "we can combine experience and behavior under the inclusive term, 'activity,' and say that psychology is the study of the activities of the individual as an individual" (Woodworth, 1930a, p. 331). In turn, physiology as the study of the activities of parts of the organism, and sociology the study of groups of individuals would cover all the positive findings of behaviorists as well as introspectionists, while abandoning their problematic "taboos". Exactly whom initially set up these taboos, and what they were is stated rather clearly in Woodworth's autobiographical statement also from 1930:
"My bogey men -the men who most irritated me, and from whose domination I was most anxious to keep free- were those who assumed to prescribe in advance what type of results a psychologist must find, and within what limits he must remain. Münsterberg was such a one, with his assertion that a scientific psychology could never envisage real life. Titchener was such a one, in insisting that all the genuine findings of psychology must consist of sensations. Watson was such a one, when he announced that introspection must not be employed, and that only motor (and glandular) activities must be discovered. I always rebelled at any such... [a priori] table of commandments" (Woodworth, 1930b, p. 376).
Though in need of further elaboration, Woodworth's general arguments seem perfectly admissible and they raise a host of historiographic questions including: How far did Woodworth, himself, proceed along the dynamic psychology path outlined above?; Were his arguments and elaborations adopted by the subsequent experimental psychology tradition?; and If they were not sufficiently adopted, what disciplinary forces held such an adoption back? While bearing these questions in mind, let's take special notice of two central points: (1) Why Woodworth believed that "activity" (acting, doing, performing) along with their "ends" or "motives" were so important to study; and (2) That it was in the hope of studying both that his S-O-R formula for psychology was put forward.
"Motivation has always seemed to me a field of study worthy to be placed alongside of performance [behaving].... We need a study of motivation in order to understand the selectivity of behavior and its varying energy. In my books I have sought repeatedly for a formula that should bring motives right down into the midst of performance instead of leaving them to float in a transcendental sphere" (Woodworth, 1930b, p. 371).
In utilizing the "mental activity" concept and in emphasizing the importance of studying "motives," Woodworth's intent is to provide a means by which the discipline can use the objective notions of cause and effect in an internally dynamic and developmental manner rather than the merely external mechanical manner that was characteristic of Watson's behaviorism. As outlined below, the "formula" Woodworth came up with -while initially stated in an expanded S-R plus "central tendencies" manner (1921)- was amended "repeatedly" to became various versions of Stimulus-Organism-Response. Although these new formulas addressed certain deficiencies of the discipline, they also contained their own difficulties, which -in my opinion- served in combination with other disciplinary forces to preclude the adequate fruition of Woodworth's above named intent, and forestall their adequate uptake into the subsequent tradition of empirical psychological practice.
Well, that's the generalized overview of our initial considerations. What now follows is a detailed account of Woodworth's all important S-O-R hinge argument upon which the remainder of Section 5 and much of the remainder of this course will depend. If I can convince you of the soundness of Woodworth's intent (to provide a "dynamic" S-O-R account); and if I can convince you of the disciplinary relevance of E.C. Tolman's "molar" behaviorist approach -as well as indicate the inherent limitations which resided in them both,- then our joint retrospective passage through the problematic "operationist era" of psychological research and the ensuing disciplinary "crisis of relevance" will not be burdened with conceptual or contentual difficulty but will constitute a valuable object lesson in what to avoid in your own subsequent career. So listen up because this part of the Section is really important! It will also be told in a way that you may not be accustomed to, or even encounter again for some time if at all.
Rise of the "molar" S-O-R formulas and early Variable models (Woodworth and E.C. Tolman)
While Woodworth was sifting through the existing intellectual products of the whole discipline (and presenting various versions of "S-O-R" to encapsulate them), E.C. Tolman's systematic energies were being focused upon the manner in which key terms in the learning subdiscipline might be brought under experimental scrutiny. The two efforts overlapped considerably when it came to portraying psychological experiments as the empirical investigation of connections between "independent and dependent variables." Although their respective early variable models were intended to support similar molar S-O-R rather than molecular S-R accounts of psychological subject matter, the ontological status of the connecting middle term in each ("organismic" vs. "intervening" variables) differed considerably. The combined significance of these overlaps and differences will be highlighted in our consideration of their respective uptake into what would become the fully operationalized variable model of subsequent empirical psychological research.
Woodworth: From augmented S-R to successive S-O-R accounts
By way of describing the troubled state of the discipline which he was now setting out to improve upon, Woodworth (1921) provides the following rather pithy footnote: "First psychology lost its soul, then it lost its mind, then it lost consciousness; it still has behavior, of a kind" (p. 2). In order to better reflect the broad practical and empirical concerns of contemporary psychologists, the definition of subject matter needed to be revised away from the former false choice of either introspective content or observable behavior toward the more inclusive new concept of mental activity.
Woodworth recognized rather early on that Watson's radical behaviorist system was the mirror image of Titchener's introspectionist system. Structuralism focused on the "How and What" of consciously experienced content; Watson's system focused on the "What and How" of overt behavior. It was just as mechanistic, elementistic, and associationist as structuralism but concentrated upon a different level of psychological subject matter. The notions of stimulus and response now constituted the fundamental units of such analysis; just as the elements of "sensations, image and feelings" did in Titchener's system. The behaviorist's program to date was simply one of translating the old mental mechanism into stimulus-response terminology (After Hillner, 1984).
In contradistinction to these, Woodworth's "dynamic" psychology (1918 onwards) "refuses to be a party to any such mutilation" of psychological subject matter (1930a, p. 333). Stated plainly, any psychology that does not set out to answer all of the journalistic "W-Fives" (Who, What, Where, When, and Why) didn't have any real chance of answering the much related "How" question! Such approaches to psychology were intellectually and empirically shackled from the outset. Hence Woodworth embarkes upon a joint emphasis on motivation (the functional aspect of internal conscious or "near conscious" content), as well as the externally observable (behavioral-performance) aspects of mental activity -the latter of which Watson (1914) himself had recognized as also "functional" in the physiological process sense of the term.
As that era's chief metatheoretician, Woodworth produced a succession of works to remedy what he viewed as a falsely constrained disciplinary situation. He begins in 1921 with an expanded S-R analysis -where he argues like Dewey, (1896) that these functional categories of analysis should not be regarded as separate disjointed events occurring in a sequence- and his efforts culminate in 1934 with a full-fledged swing away from S-R toward a "dynamic" S-O-R account accompanied by a complementary experimental methods rationale.
Woodworth's early 'expanded S-R' account
The following two diagrams and argumentative examples from Woodworth's 1921 account will serve to indicate the intellectual baseline of his revisionist efforts in this regard. Although Woodworth carefully prepares the way for his readers by providing various informative ground-up statements in the proceeding chapters ("Reactions" and "Reactions of Different Levels"), the crucial 1921 chapter for our present concern is "Tendencies to Reaction" (pp. 68-88). It is here that he suggests that "no violence has been done to the general conception of a [Stimulus-Response] reaction" by the "addition" of seemingly teleological concepts like 'motive, directive tendencies and preparatory reactions'" (p. 84). So, let's go through this chapter to find out what Woodworth is on about.
One advantage of basing our psychology on reactions, he suggests, is that it keeps us close to the ground (within the realm of concrete, specific observations rather than "fanciful" speculation). "Whenever we have any human action before us for explanation," we have to ask "what the stimulus is that arouses the individual to activity and how he responds" (p. 68). Stimulus-response psychology is "solid;" for if it can "establish the laws of reaction," so as to predict what response will be made to a given stimulus, it furnishes the 'knowledge that is power'. "Perhaps no more suitable motto could be inscribed over the door of a psychological laboratory than these two words, 'Stimulus-Response'" (p. 68).
"But," he writes -and this is the crucial part- "we must not allow it to blind our eyes to any of the real facts of mental life; and at first... it seems as if motives, interests and purposes [do] not fit into the stimulus-response program" (p. 69). To emphasize this point, and in order to prepare us for what he believes is the proper resolution to issue at hand, Woodworth makes the following contrast: Suppose we are looking out on a city street during the noon hour. We see numbers of people standing or walking about, looking at anything that chances to catch their eye, waving their hands to friends across the street, whistling to a stray dog that comes past, etc. These people are responding to stimuli and there is no difficulty in fitting their behavior into the stimulus-response scheme. But here comes someone who pays little attention to the sights and sounds of the street, simply keeping his eyes open enough to avoid colliding with anyone else. He seems in a hurry. He is not simply responding to stimuli, but has some purpose of his own that directs his movements. Here is another who seems to be looking for someone in particular, making him extra responsive to certain sorts of stimuli.
"Now it would be a great mistake to rule these purposeful individuals out of our psychology" (p. 70). We wish to understand busy people as well as idlers:
"To complete the foundations of our psychology, then, we need to fit purpose into the general plan of stimulus and response. At first thought, purpose seems a misfit here... But if we could show that a purpose is itself an inner response to some external stimulus, and acts in its turn as a 'central stimulus' to further reactions, this difficulty would disappear" (Woodworth, 1921, p. 70, emphasis added).
The purposeful person, Woodworth suggests, "wants something he has not yet got, and is striving towards some future result" (p. 71). Whereas a stimulus pushes him from behind, a goal beckons to him from ahead. This "element of action directed towards some end" is absent from the "simple" (physiological reflexive or casual) response to a stimulus. Thus Woodworth presents the following diagram to allow for "action steered in a certain direction by some cause acting from within the individual" (p. 71).
Woodworth's aim here is to find a way around what would later be called (by A.N. Leontiev, 1979) the "postulate of environmental immediacy," which was inherent in the behaviorist S-R scheme of John B. Watson. To this extent we can be sympathetic to Woodworth's aim but should also be somewhat wary of his proposed solution as depicted above because among other things he would later revise and then partially repudiate it on the grounds that it remains too "linear," static and mechanical overall. We will indicate why shortly.
For the time being, however, Woodworth accepted this depiction and sought to indicate the specific mechanisms by which purpose acts as a "central stimulus." Even at this time, however, he is careful to point out a vertical (evolutionary) dimension to the scheme he is presenting. "Purpose" is not the best general term to cover all the "internal factors" that direct activity, he argues, since this word implies conscious foresight of the goal. This "highest level of inner control" over behavior differs from the "two levels" below which, while being carried out "towards a certain result" do not involve "conscious foresight of that result" (p.71):
"The lowest level, that of organic states, is typified by [physiological] fatigue. The middle level, that of [individual] internal steer, is typified by the hunting dog, striving towards his prey, though not, as far as we know, having any clear idea of the result at which his actions are aimed. The highest level, that of conscious purpose, is represented by any one who knows exactly what he wants and means to get it" (Woodworth, 1921, p. 72).
While Woodworth admits that no single word (including motives) is proper to cover all three levels of directedness toward ends, he nonetheless suggests that "Motives" will serve -as long as we agree that a motive is not always clearly conscious or definite "but may be any inner state or force that drives the individual in a given direction" (p. 72). In my opinion, this over-generalization of a perfectly useful colloquial term beyond its commonsense meaning is both uncharacteristic of Woodworth and extremely unfortunate. If there are indeed three levels of analysis to be differentiated here, why not explicitly outline them by providing different terms for the kinds of activity being carried out and the conditions under which (or ends toward which) they are being carried out? It should be mentioned that it would be a long while before A.N. Leontiev's Activity Theory did precisely that!
Thus, from our current historically retrospective vantage point, when Woodworth (p. 74) asks whether "the facts already cited compel us to enlarge somewhat" the conception of a S-R reaction, we can answer a qualified 'No' to his definitive 'Yes.' Recall that Dewey (1896) had already suggested that while S-R analysis works for automatic physiological reflexes, it fails to capture the intentional aspects of even the simplest forms of individual voluntary acts (let alone the more complex ones). Instead of expanding the scope of a fanciful analytical metaphor, why not just give it up? Dewey in his own arcane prose tried to argue this point by rejecting both the "reflex arc" and "reflex circuit" view of intentional human action (see Section 4). Woodworth, like Dewey and Carr too, seems to know "what he wants" (a levels approach to mental activity) but can't exactly find the conceptual means to get it!
Meanwhile, having answered "yes" to the above question, Woodworth proceeds to expand his S-R account still further in an attempt to address the issue of the "selectivity" of these directive tendencies towards ends (which tendencies will actually result in the carrying out of a response and which will not). To address this selectivity issue, Woodworth utilizes the concept of preparatory reactions (labeled as "P").
It is here that we start to get a glimpse of the linear-mechanical nature of his initial (1921) expanded S-R scheme. The more terms he plugs into the above schematic space between Stimulus and Response, the more mechanical the account appears. The immediate question raised by Woodworth himself is one of the nature, scope, and basis of these preparatory "reactions". As in the case of "motives" (as defined by him) these "reactions" are said to operate on three distinct levels. They seemingly depend upon "organic states" (e.g., physiological reflexes, hunger, muscle fatigue); and or prior "conditioning;" or "learning" depending upon the related level of mental activity being considered. The examples of the functioning of preparatory reactions provided by Woodworth (pp. 74-82) likewise nearly run the gambit of conceivable generality: from "neural" preparation, to the body orientation of rats towards the designated box of a delayed reaction experiment, to the seeking of food or drink by needy animals, to baby's refusal of a bottle, to Woodworth's own rising from his chair in order turn on a light for reading in the late afternoon.
I say "nearly" above because there is no reason why -according to Woodworth's presented scheme- that a college or university education itself should not also be termed a "preparatory reaction." Yet, as in the case of his overgeneralized"motive" definition, one is left with the question why there are not different terms being utilized for each of these seemingly very diverse albeit "preparatory" processes. As we will show below, the organismic and individualized analysis exemplified here is a recurrent theme in all of Woodworth's successive works. He never really manages to move beyond that level of analysis and this is a very important point to note for future reference.
Woodworth's shift to S-O-R
On the more progressive side of things, however, Woodworth does eventually recognize that his early "expanded S-R account" -which he originally claims to "do justice to all of human behavior" (1921, p. 84) is not, in fact, adequate to the job. This transition toward a relatively fuller S-O-R account takes place gradually for him between 1921-1934.
In 1926, for instance, while still proposing an expanded S-R account, he is careful to address the issue of the apparent linearity of the early account in particular. After opening the paper with a direct reference back to Dewey and James, Woodworth (p. 122) first reiterates his 1921 point that a stimulus is not to be identified with cause; and then suggests too that the often assumed "serial order" of events (S-R) is also a mistake because "very seldom does a stimulus find the organism in a completely resting, ... unpreoccupied state" (p. 124).
"Ordinarily, a stimulus breaks in upon some activity in progress... This activity has a trend towards some goal, immediate or remote. We have, then, not first stimulus, then activity of the organism; but first an activity going on, next an intercurrent [disrupting] stimulus, and then the activity modified in response to the stimulus.... What we see is an activity going forward in a definite direction and rendering the organism unresponsive to certain stimuli, while unusually responsive to others" (Woodworth, 1926, pp. 124-125).
This progressive (though still organismic and individualized) theme is further elaborated in the 1929 text, where, -after mentioning that the old S-R account is "sometimes interpreted to mean that if you know the stimulus, you can predict what the response will be"- Woodworth presents the adjacent straight-line Stimulus-Organism-Response diagram (p. 226) to distinguish his position from that older view.
Woodworth's new S-O-R account, however, reaches its height in the 1934 edition with an explicitly stated continuously environmentally interactionist, and dynamic S-O-R account of subject matter. In the two following diagrams (from Woodworth, 1934, pp. 8-9), W=world; S=stimulus; O=organism; and R=response:
While this new account was most certainly a progressive step at the time it was proposed, the main question which concerns us at our present historical juncture is whether the "continually interacting" (reciprocal) relationships depicted in these S-O-R diagrams really solved the problems indicated above, or whether they were just as inadequate to that task as Woodworth's initial expanded S-R account had been. A definitive historical judgment on the methodological viability of the S-O-R account, however, will have to await our fuller assessment of the two most cogent ways that the new formula was applied by Woodworth (1934): (i) to define the very structure of psychological experiments; and (ii) to make pronouncements on the heredity vs. environment debate. To gain a better grasp of the disciplinary setting in which Woodworth's descriptive S-O-R formula was initially put forward, however, we must turn to the roughly contemporaneous efforts of E.C. Tolman.
E.C. Tolman and the early application of 'molar' Behaviorism
Unlike Woodworth (whose disciplinary contributions were ones of methodological, historical, and metatheoretical analysis), Edward Chance Tolman (1886-1959) was primarily an experimental psychologist who oversaw a rather circumscribed, hard-nosed empirical research program at the University of California (Berkeley). Tolman utilized the forthcoming evidence in support of a set of argumentative propositions which he successively called: "purposive" (1925, 1932), "molar" (1926, 1932), "operational" (1936), and "cognitive" behaviorism (1948).
While the structure of his research program and subsequent analysis adhered roughly to the molar S-O-R account outlined above, Tolman himself forswore to avoid making pronouncements on the ontological status of what he called "intervening variables" (those that reside between observable Stimulus and Response variables). In his 1925 critique of "mentalistic" positions (like McDougall, 1912; and Woodworth, 1918), for instance, Tolman argued that "purpose" need not be inferred as an intentional power of the mind but was a mere matter of referring to the goal-directedness of observable behavior (see also Tolman, 1920, 1923, 1935). Accordingly he has subsequently been classed by historians of psychology as a "methodological" rather than a "metaphysical" (mentally eliminative) behaviorist.
From the time of his earliest argumentative and empirical review articles (1922, 1932) through to his major book-length or summary reviews of the molar behaviorist maze learning experimental tradition (1938, 1948), Tolman argued that early S-R theorists by adopting the language of reflexes had mislead themselves into a reductive molecular account. They had portrayed observable behavioral responses as merely equivalent to what is meant in physiology by muscular reflex. Watson, in particular, he suggests, had vacillated between those two different notions of behavior -psychological and physiological- without ever understanding how they differ. For Tolman, behavioral responses are more than the sum of their physiological parts. Behavior, as such, is an "emergent phenomena" which has descriptive and definitional properties of its own: "We shall designate this as a molar definition of behavior" (Tolman, 1932, p. 6).
Given the bearing of Tolman's research and reviews on many of the contemporaneous disciplinary debates already mentioned, we will briefly summarize a few of the most relevant empirical studies carried out in this tradition (including Simmons, 1924; Elliot, 1928; Blodgett, 1929; MacFarlane, 1930; Tolman & Honzik, 1930a&b; Wickens, 1938; Tolman, Ritchie, & Kalish, 1946). The essential tension or strained inconsistency between Tolman's initially assumed ontologically agnostic stance toward mental processes and his eventual recognition of goal-expectancy, global avoidance responses, place learning, and cognitive maps as psychological "entities" will be highlighted along the way.
Context and debates of the Berkeley research program
Although Tolman (1932) would eventually overstate the case for the generality of the methods and the conclusions drawn from these experiments (as being suitable for investigating "everything in psychology save language and society"), they did collectively constitute a significant contribution to the reorientation of early behavioral research away from merely physiological and towards at least rudimentary psychological questions. They warrant our historical attention because it was by way of reference to them that Tolman was first able to abandon Watson's muscle twitchism, and then counter Clark L. Hull's newer, though equally molecular, "reinforcement gradients" form of behaviorism.
The widest debate entered into by Tolman's Berkeley lab was regarding: Which (or how many) of the available associationist laws of conditioning to accept. Recency and frequency, or the "law of effect" too? In some respects this was the most general debate they entered but it was also the easiest for them to resolve definitively. Here, Tolman took up the middle-ground between Watson and Thorndike so some initial commentary on their respective points of view is necessary before wading into the empirical evidence mobilized in this regard.
Watson (1914) had proclaimed that all learning in rats, cats, and humans is dependent upon and requires immediate reinforcement. He rejected Thorndike's (1890s era) law of effect (regarding pleasant or unpleasant results) and maintained that the principles of recency and frequency of reward are the only necessary principles needed to explain how learned habits in animals and man occur.
Thorndike's account of his cats (see Section 4) was one of "trial-and-success" learning, with the neurological "stamping in" of the habits which immediately precede escape from the puzzle box -without reference to use of "ideas." Watson further radicalized this rejection of ideation by suggesting that there was no room in psychology for even such a backwards looking neurological account of new habit formation because not only did it seem to assume conscious awareness in animals, it also smacked of "teleology" which he viewed as hopelessly metaphysical. All accounts of cause and effect for Watson followed the linear mechanical (efficient) causal S-R chain pattern. Both Woodworth's continuously interactive S-O-R and Tolman's purposive behaviorism would take exception to this one-way linear aspect of Watson's account.
In Tolman's 1915 Harvard dissertation, he compared the memory of nonsense syllables learned in the presence of noxious and pleasant odors as presented to the nostrils of human subjects by way of an olfactory apparatus. Likewise, one of his first few publications (Tolman, 1917) reported a retroactive inhibition effect under such conditions.
Upon reaching Berkeley, Tolman like many others of the era made simultaneous use of texts by Thorndike (1911) and Watson (1914) to teach classes in comparative psychology. So, it should not be surprising that while he agreed with Watson and Thorndike regarding the bracketing of reference to introspective conscious states in animals and man, he also sought to temper the radicalism of Watson's complete rejection of goal-directed behavior.
On the whole, the research program of the Berkeley lab was aimed at drumming up empirical evidence for the latter options of the following five interrelated issues: (I) Passive peripheralism or active expectancy of reward?; (II) On Laws of association: mere recency and frequency or effect too?; (III) On the perceptual processes used by rats to run mazes: additive concatenation of molecular kinesthetic responses or molar place learning?; (IV) In humans: muscle twitches or global response learning?; and (V) Countering Hull: numerical response gradients at maze choice points or cognitive maps? So, let's take a look at the evidence.
(I) Passive peripheralism or active expectancy of reward?
Watson had put forward a thoroughly molecular and largely passive-mechanical account of behavior. Observable behaviors of all sorts are triggered by immediately present environmental stimuli on the basis of recency and frequency. When carefully studied in the laboratory, they can be rendered physiological by analyzing them into the complexes of smaller muscular or glandular components from which they are made. Tolman understood behavior, however, as purposive. For him, the aim of laboratory study was to analyze the goal-directed nature of integrated molar acts.
An initial series of investigations presented by two of Tolman's students (R. Simmons, 1924; and M.H. Elliot, 1928) constitute an important early phase of the empirical attack on Watson's above stated "peripheralisms." Simmons reasoned that if Watson was correct, there should be no measurable difference in the influence of different sorts of reward on the maze performance of rats because, after all, a maze was an apparatus in which an experimenter could render the recency and frequency for each of various kinds of rewards the same. Simmons' 1924 work is notable, therefore, because it was the first to clearly indicate that a hierarchy of reward preferences exists for rats in a maze.
Simmons ran separate groups of equally food deprived rats through a simple alley maze and measured the average time it took each group to master the maze for different food "incentives". With the time from start to food box being defined as a "run," and with a successful run being defined as an error free (direct route to the food) run, and with three successful consecutive runs being defined as "mastery," Simmons found that: (i) On average, rats rewarded with bread and milk ran fastest; (ii) those rewarded with sunflower seeds ran the next fastest; and (iii) those that were simply removed from the goal box after each successful maze trial, mastered the maze the slowest. Certain rewards, he concluded, were more "demanding" (motivating) on maze performance than others.
Elliot (1928), also weighed in on this issue of "reward demand." When rats that had been trained (had already mastered the alley maze -shown right) with a "highly demanded" reward, encountered a less demanded reward on later trials, they ran the maze more slowly and made more "errors" on those subsequent trials. Alternately, rats trained first with a "less demanded reward" improved their average run performance when the higher demand reward was substituted. Elliot concluded that maze performance is not a direct result of mere reinforcement, it was also a function of the kind of reward.
For Tolman (1932, 1948) the Simmons research (showing the relative effectiveness of various incentives on maze running performance) and the Elliot research (showing the effect on maze running of changing from high to low demand incentives) was clear evidence that rats acquire specific expectancies about the goal to which their behavior is directed. Another Tolman student, O.L. Tinklepaugh we should also note drew similar conclusions from his 1928 study with monkeys. In other words, the former linear mechanical S-R unit of Watson, had now become expanded to a forward-looking "Stimulus--Intervening Variable--Response" analysis in Tolman and his students.
(II) Laws of association: Recency and frequency or effect too?
In a related set of findings, it was H.C. Blodgett (1929) who challenged Watson's most generalized assumption that learning could not occur in the absence of reinforcement. Just how simple it was to resolve this issue is indicated by the rather uncomplicated structure of the Alley Maze used by Blodgett. Starting (bottom left) the rats proceeded through various one-way doors (D) to the Food box (top right).
Three groups of rats were trained to run this Alley maze. Group 1 (the control group) was rewarded with food every time they reached the goal box. Group 2 (the first experimental group) did not find food for the first six days of training, but were merely removed once they reached the goal box. Group 3, (the second experimental group) ran without food reward for two days, found food on the third day, and continued to find it for the rest of the experiment.
Both experimental groups showed a marked reduction in the number of errors the day after the initial transition from nonfood to food reward conditions and continued this improved performance thereafter. Tolman & Honzik (1930b) repeated the experiment with some variations to produce the following table (reproduced from Hilgard, 1987 in its entirety).
Clearly these rats had "learned" something during the nonfood trials and Tolman suspected that they had become aware of the surface layout of the maze (see also Tolman & Brunswick, 1935). Tolman (1932) called the initial learning occurring during the non-reward trials "latent learning" and suggested that latent learning was a pervasive aspect of everyday experience for both rats and human beings (p. 343). Since rats did in fact learn in the absence of food reward, Tolman also made the explicit distinct between "learning" (which can occur without reward) and "performance" (which is heavily dependent upon reward) at this time.
(III) Which perceptual processes were used? -additive concatenation of molecular kinesthetic response versus molar place learning.
Similarly, with regard to the debate over the actual perceptual processes utilized by rats to run mazes, recall that both Watson (1907a), as well as Watson & Carr's (1908) analysis of their "Kerplunk" experiment, had argued that kinesthesia (bodily-muscular sense) was the predominant, if not the only means used. The combined results of various experiments presented by D.A. MacFarlane (1930), however, served to counter that hypothesis.
MacFarlane first trained rats to swim a maze in order to obtain food placed on a raised central goal platform. When the rats had learned their way through the maze, a false bottom was inserted so that they could now wade towards the food platform. After a transient period of disruption, it was found that the rats soon made no more errors than in the original mastered training trials. Further, once all the water was drained from the maze (so that the rats were now required to run through the maze), the same effect was found. These studies, therefore, provided evidence of the flexibility of goal oriented behavior.
The main empirical finding that subsequent success was not effected by a change in the modus of locomotion, strongly suggested that what was being learned was where the reward was located rather than what motor responses were needed in order to reach the goal. In other words, the rats were not as mindless as Watson and Carr had made them out to be. Whatever they had originally learned, it could not have been the mere response of performing some specific kinesthetic swimming motion associated with the stimuli at each choice point in the maze.
According to Tolman's (1932) coverage of these experiments, the rats had not learned a mere series of responses but instead the spatial layout of the maze (pp. 77-82). This "cognitive map," as he called it, could then be used to get from the start to the goal in any of a number of ways (swimming, wading, running). While these experiments certainly show that something more than a mere concatenation of discrete or successive kinesthetic S-R associations was learned, they did not on their own resolve the question as to whether it is anything like a cognitive map or not. For this, more evidence was required and Tolman would have to utilize that evidence repeatedly to counter the views of both Watson and Clark L. Hull (see that evidence presented under "V" below).
(IV) Human research: Muscle twitches or global response learning?
For now, however, we should probably follow the order of the above Watson account which moved into the arena of human research by way of utilizing the technique of shock avoidance with the finger reflex apparatus (1916, shown above). In Watson's view, behavior in human subjects could still be defined as molecular muscular responses caused by the specific stimuli with which they had become mechanically associated by way of recency and frequency. In Tolman's view, however, a molar response category was associated by the organism (human or animal) within a given stimulus situation.
For example, if a person learned to withdraw their finger from an electrode when a warning signal preceded an electric shock, then the molecularist would say that a specific conditioned muscular reflex has been learned. By contrast, a molar behaviorist would claim that a global avoidance response had been learned. It was D.D. Wickens (1938), who did the study to test the respective veracity of these two accounts for this particular experimental situation. He first taught the above "Watson-Lashley" finger withdrawal response to his human subjects, and then turn the subject's hand over to see what would happen next. Since this experimental procedure necessitates that an anatomically "antagonistic" muscle group now needs to be utilized to carry out finger withdrawal, the Watsonian position predicts that a new muscular reflex will have to be learned (as the original one will drive the finger into the electrode). Tolman's position, however, predicts that the subject will immediately avoid the shock since they have already learned a global (molar) shock-avoidance response (not a specific muscular reflex). The Wickens results supported Tolman's prediction rather decisively.
(V) Response gradients or Cognitive Maps?
Finally, when the Yale-based Clark L. Hull came on the scene with his molecular response gradients hypothesis, Tolman's Berkeley lab already had most of the empirical ammunition readily at hand to cut his hypothesis down. Tolman's conception of "purpose" had expanded over the years -moving from the status of an hypothetical intervening variable to a near cognitive power- but he always had suggested that goal-oriented responses were a real and important aspect of observable behavior for psychology to study. Hull on the other hand, set out to explain purpose and cognition away by working out an hypothetical-mathematical account of the mindless mechanical processes upon which our belief in those intervening entities might be based. Just as Newton had derived the motions of the planets from a small set of physical laws, so Hull (1934a&b; 1935; 1943a&b) proposed to predict the behavioral motions of organisms from a set of mathematically describable molecular quantitative response gradient laws.
One of the classic studies Tolman utilized to emphasize that rats learned the layout of a maze was first described in Tolman & Honzik's article "'Insight' in rats" (1930a). Although it predates Hull's reinforcement gradients hypothesis, it is still instructive in various ways. First of all, this study utilized what is called an elevated maze (similar to that later used by N.R.F. Maier -shown right- but different in actual layout). Note that these elevated mazes contain no walls and, at least potentially, allow the rats to take visual stock of the layout of the maze structure. In Tolman & Honzik's study, however, it was the rather clever layout and "path-blocking" procedures used by the experimenters that seemed to provide decisive evidence for the use of cognitive maps by rats.
After allowing the rats to explore the elevated maze freely, a food reward was then placed in the goal box and the animals quickly began to favor the shortest (straight) route from the start box. Once this habit was formed, however, the experimenters blocked the shortest route at block point 1, to see what the rats would do. Upon encountering block point 1, the rats tended to backtrack and take the next shortest (leftward) route and this new habit rapidly became more frequent on subsequent trials.
Note that this initial backtracking behavior (on its own) is consistent with not only the learning of specific response hypothesis (a la Watson) but also both Tolman's cognitive maps hypothesis and Hull's numerical reinforcement gradients hypothesis. According to the latter, the rats favoritism of the second shortest route is a wholly mechanical affair involving the bodily computations of previous route-taking behavior preceding the blockage. No matter, however, because the next phase of the experiment decisively ruled both Watson's and Hull's hypotheses out of contention.
When the initial block point was removed, and a new block placed at block point 2, both Watson's and Hull's hypotheses would predict that the rats would again backtrack to attempt the leftward second route, but the data did not bear this sort of prediction out. Instead, they backtracked to take the rightward (long) route directly to the food box.
Tolman & Honzik (1930a), it is true, overstated their case for they suggested that this latter behavior was proof of "insight" in rats on par with that found in Kohler's ape experiments -an issue we will come back to later- but again no matter. The data itself had shown rather clearly that rats could utilize some sort of awareness of maze layout to reach a goal. Tolman's view that maze learning is the acquisition of knowledge about the environment had born rather pungent experimental fruit which Hull and his supporters never really managed to swallow.
To this ready arsenal of prior findings was added a few notable new findings too. Some of these were summarized in Tolman's 1937 APA presidential address "The determiners of behavior at a choice point" (Tolman, 1938), but it must be mentioned that no death blow was struck there to the Hullian hypothesis. This would only come later when it was finally recognized that one way to assess the likely relative importance (preponderance) of place versus response learning is to assess the relative ease with which they are learned respectively.
Tolman, Ritchie, & Kalish (1946), therefore, compared place learning versus response learning in two different groups of rats by utilizing the ingeniously simple elevated maze situation (shown below). One group of rats (the "place" learners) always found food at the same place, even though depending upon where they started the maze on any given trial -S1 or S2- they might be required to turn either left or right at the choice point (C) to obtain food. The motor responses in this place learners group differed, but the food location was always the same (F1).
For the other group (the "response" learners), it was the food that was shifted so that no matter where the rats were started -S1 or S2- in any given trial they were always required to turn in the same single direction (e.g., left) to obtain the food.
The results showed that the place learners performed significantly better than the response learning group and five of the latter group did not master the maze situation even after seventy-two trials.
Despite various subsequent equivocations from within the Hullian camp (including Kanner, 1954), it should be pretty clear even from this somewhat impoverished sampling of a very rich and intricate tradition of research, that Hull's position was made untenable. Thus Tolman (1948), in looking back over nearly 20 years research could say with some confidence that maze learning in rats "consists not in stimulus-response connections but in the building up in the nervous system of sets which function like cognitive maps" (p. 193).
We have noted above that Woodworth advocated the use of experiments as one of the empirical methods of psychology, and that Tolman both carried them out and oversaw an active lab at Berkeley in the tradition of molar behaviorist experimentation. We should now turn to a closer account of their respective early "variable" models of experimental research because this comparison will be useful in our consideration of the subsequent "operationalist" and "crisis of relevance" eras of the discipline.
How experimental psychology got its "variables"
Having made the above contrasts (regarding both Woodworth's early S-R vs. later S-O-R versions of psychological subject matter; and Tolman's molar behaviorism vs. Watson and Hull), a further comparison can now be made between Woodworth's professional strivings to popularize the exact nature of psychological experimentation with the contemporaneous use of the term "variables" by E.C. Tolman and others. We will then make a few comments on their respective uptake into subsequent General experimental psychology.
The now standard North American psychology textbook definition of an experiment as the systematic assessment of the mathematical relationship between "independent and dependent variables" (the IV-DV model), was a disciplinary product of the early 1930s-1970s (Winston & Blais, 1996). The term "variable" as it related to empirical psychology was first introduced sporadically in E.G. Boring's The physical dimensions of consciousness (1933). Tolman, Skinner, and others also began to use the term at this time but it was Robert S. Woodworth (1934, 1938) who popularized and formalized the "IV-DV" terminology through his widely read introductory text, Psychology, and his 1938 "Columbia Bible," Experimental Psychology (see Winston, 1988, 1990).
Independent, Organismic, and Dependent variables (Woodworth)
The first two editions of his Psychology utilized a rather loose and indefinite conception of psychological experimentation with systematic variation of conditions in the laboratory being viewed as one kind of experiment and the giving of a mental test to compare individuals as another kind. But by the third edition, a more particular sharpened definition of experiment was presented.
As indicated in the figure (right) from Woodworth's (1934) text, it is here that he first suggests that only those studies that manipulate one condition (the Independent variable under consideration) while holding all others constant are properly called experimental ("I" = independent variable; "C" = held constant; and "D" = dependent variable). Experimental research is here depicted as the active manipulation of an independent variable to discover the preexisting cause of the resulting dependent variable under study.
"The rule for an ideal experiment is to control all the factors or conditions, to keep all of them constant except a single one -which is then the independent variable- and to vary this one systematically and observe the results" (Woodworth, 1934, p. 19).
While Danziger & Dzinas (1997) -as well as Danziger (1997)- have suggested that reference to Galtonian Anthropometric statistics played a major role in Boring's initial adoption of the concept of "variables" (as that which is studied in psychological inquiry), Woodworth's 1934 account is most notable in that it seems to be demarcating a disciplinary divide between "experimentalist" and "correlationist" variable research with one branch being university based and the other applied.
This implied demarcation is made explicit in Woodworth (1938) when he reiterates his earlier sharpened definition of experimentation and distinguishes it as different from correlational research in that it seeks out causes rather than mere interrelations between effects, thereby explicitly excluding mental testing from the Provence of experimental psychology.
"To be distinguished from the experimental method, and standing on a par with it in value, rather than above or below, is the comparative and correlational method. It takes its start form individual differences. By use of suitable tests, it measures the individuals in a sample of some population, distributes these measures, and finds their average, scatter, etc. Measuring two or more characteristics of the same individuals it computes the correlation of these... and goes on to factor analysis. This method does not introduce an 'experimental factor'; it has no 'independent variable' but treats all the measured variables alike. It does not directly study cause and effect. The experimentalist's independent variable is antecedent to his dependent variable; one is cause (or part of the cause) and the other effect. The correlationist studies the interrelation of different effects" (Woodworth, 1938, p. 3).
The ongoing professional divergence between these two groups of variable psychologists was initially manifested in the formation of the American Association of Applied Psychology (est., 1938), but was suspended by mutual consent during W.W.II and in 1945 the AAAP was amalgamated back into an expanded APA Divisional structure (see Hilgard, 1987, pp. 758-761). Despite these postwar efforts at affiliational solidarity, the divides between those practicing primarily experimental and correlational methods remained to such an extent that L.J. Cronbach (1957) would eventually describe "The two disciplines of scientific psychology" with one being the domain of the university laboratory and the other being that of applied or clinical psychometrics (in therapeutic assessment, military, educational, or higher educational entrance exam settings). Likewise, on December, 31, 1959, the Psychonomic Society, being just one of a succession of experimental psychologist splinter groups, was also officially formed.
Noting these affiliation rifts between the mid-20th century experimental and correlational subdisciplines is quite helpful for our present historical purposes. First, it allows us a distinct retrospective advantage over early psychological writers such as Boring, Tolman, S.S. Stevens, and Woodworth who could only have guessed at the eventual combative professional relations between these two divergent empirical research traditions. Secondly, it allows us to recognize the import of contextualizing and analytically unpacking the varied assumptions of successive versions of psychological operationism. Two of these have been labeled by Tim Rogers (1989, 1991) as experimental and correlational respectively. A third version, which attempted to smooth over the above disciplinary rifts, has more recently been labeled as "convergent" operationism by Randolph Grace (2001 a & b).
Stimulus, Intervening, and Response variables (E.C. Tolman)
As mentioned above, Woodworth (1929, 1934) abandoned his own initial S-R viewpoint to adopt an S-O-R account of subject matter in which it is necessary to know one's organism. Tolman, using a slightly different perspective, gradually came to a similar conclusion. He is credited with having been the first to clearly formulate the concept of the "intervening variable" within the behavioral tradition (1935; 1938; 1948) -a discursive concept which is still utilized in much of the contemporary experimental and cognitive psychology literature.
The linear (passive, mechanical) S-R unit of Watson had become expanded to a forward-looking Stimulus-Intervening variable-Response analysis in Tolman and his students. Like Woodworth (1921), Tolman was attempting to reject Watson's postulate of environmental immediacy. Something is going on inside the organism that mediates the link between what is learned (or perceived) from the stimulus environment, and what particular behavioral response is "performed" and thereby observed by the experimental researcher. The observable properties of behavior included the goal-directedness of that behavior. Recall that for Tolman, it was a matter of observable empirical fact that rats could utilize some sort of awareness of maze layout to reach a goal. Further, the comparison of groups of rats under conditions of place learning versus response learning indicated that some sort of building up in the nervous system of sets functioning like cognitive maps was at work.
By eventually replacing the passive slot-machine view of Watson with an adjustive mechanism ("central control room") analogy, Tolman (1949a) is often said to have anticipated the later information processing approach of cognitive psychology (see Hilgard, 1987; Leheay, 1991).
"I do not hold, as do most behaviorists, that all learning is, as such, the attachment of responses to stimuli. Cathexes, equivalence beliefs, field expectancies, field-cognition modes and drive discriminations are not, as I define them, stimulus-response connections. They are central phenomena, each of which may be expressed by a variety of responses" (Tolman, 1949a, p. 146).
Methodologically speaking, however, his long-standing equivocal stance on the ontological status of such "central phenomena" (a.k.a., intervening variables) contributed to the ongoing uptake of experimental operationism into General experimental psychology texts as well as into the cognitive psychology movement which followed thereafter. As Tolman (1959) put it himself:
"Although I was sold on objectivism and behaviorism as the method in psychology, the only categorizing rubrics which I had at hand were mentalistic ones. So when I began to develop a behavioristic system of my own, what I really was doing was trying to rewrite a commonsense mentalistic psychology... in operational behavioristic terms" (Tolman, 1959, p. 146).
While it is true that Tolman's early conception of "purpose" had expanded over the years -moving from the status of merely descriptive intervening variable to a near cognitive power (see Tolman, 1949b)- the above quotation exposes the commonly-held and highly problematic "operationist" underbelly of both Tolman's neobehaviorist scheme of experimental research and the later so-called Cognitive Psychology tradition. Much of what would later be labeled as early manifestations of cognitive psychology is indeed a "commonsense mentalistic psychology framed in operational terms" hence the glowing references to Tolman as one plank in their initial disciplinary platform. In the sense that cognitive psychology continues to adopt Tolman's roughly mechanical 'Stimulus-Intervening variable-Response' analysis, it is merely an updated form of neobehaviorism albeit framed in "hypothetical construct" or "information processing" language.
Examples of their respective uptake into General-experimental psychology
Winston & Blais (1996) have carefully outlined the rise of Woodworth's IV-DV experiment definition in psychology over three decades (1930-39, 1950-59, and 1970-79); which as they say nicely "encompass" the respective introduction, dominance, and beginnings of doubt about the variable model of experimentation. Woodworth's initial use of the "independent and dependent variable" terminology to define experimentation increased dramatically in psychology texts from the 1930s to the 1970s:
As partially indicated in the parallelogram, the use of Woodworth's "manipulation" of an independent variable definition jumped in psychology from 5% in the 1930s (1 text, Woodworth's Psychology) to 95% of the sample from the 1970s. Winston & Blais also indicate that the adoption of this "variable" terminology appears to a relatively lesser degree in sociology texts after its adoption in psychology and in markedly lesser degree in biology and physics texts too.
"In sum, introductory psychology textbooks gradually adopted a highly uniform view of experiment as defined by manipulation of an independent variable. This uniformity was achieved relatively recently (between the 1950s and 1970s). By the 1970s, psychology texts imply that experiment is... superior to other methods. This view was not borrowed from the textbooks of other disciplines, although other disciplines may have recently begun to borrow the construction of method used by psychology texts. In physics, which psychologists traditionally take to be the model science, discussions of research method and definitions of experiment are generally absent. When physics texts define experiment, they generally do so in a much broader manner than psychology texts and with a different meaning accorded to manipulation of a variable" (Winston & Blais, 1996).
Given the influence and so-called ascendancy of experimental cognitive psychology in the decades following the 1970s, I thought it would be advisable to provide you with some specific examples (explicit textbook depictions) of experimental variables to illustrate the respective uptake of both the Woodworth and the Tolman variable models of research. Surprisingly, after having made a fairly extensive search for such specific examples in introductory texts (dating from the 1930-1990s), I found only a few texts willing to externalize their experimental-methodological assumptions in this manner. Perhaps less surprising (though nonetheless vital to note), is the fact that none of these depictions conform completely to either Woodworth's (IV-DV) or Tolman's (Intervening variable) schemes. Instead, they all to varying degrees maintain a decidedly mixed (eclectic) flavor.
For the purposes of the present discussion, two of the better diagrams have been selected. So, let's look at both to see what conclusions might be drawn out from them respectively. First up is an example from Munn et. al. (1969), which seems to have taken up a mixed version of Woodworth's views on S-O-R (subject matter) and the manipulation of "variables" as the definition of psychological experimentation:
"Variables in a Psychological Experiment. As shown in this simplified schema, response (dependent) variables are influenced by both stimulus conditions and characteristics of the organism" (From: Munn, Fernald, & Fernald, Basic Psychology, 1969, p. 24).
It is highly appropriate to find such an explicit figure in this particular text because the authors are all major figures in mid-through-late 20th century experimental psychology. Norman L. Munn (1902-1993) was initially trained in experimental animal psychology under W.S. Hunter at Clark University to receive both an MA and PhD there in 1928 and 1930 respectively (see Munn, 1980). He authored a number of textbooks with an emphasis on experimental (and then evolutionary or developmental) methods including: An introduction to animal psychology (1933); Psychology (1946); Handbook of Psychological Research on the Rat (1950); The Evolution and Growth of Human Behavior (1955); Introduction to Psychology (1962); and The Evolution of the Human Mind (1971). As the titles of his works indicate, Munn's unit of psychological analysis expanded over the years to culminate in the 1971 work -which included chapters on "Cultural Evolution&
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